|This manuscript advances an interesting, but very speculative, explanation for springtime peaks of nitrate in relatively recent Greenland snow (specifically Summit in this case). It has long been known that nitrate exhibited a broad summer maximum in preindustrial Greenland snow (as observed in firn and ice cores) but since ~ 1950 (perhaps as early as 1900 by some accounts) it has become difficult to recognize this annual cycle due to additional peaks that can occur at varied times of the year (e.g., Finkel et al., 1986; Whitlow et al., 1992; Yang et al., 1995; Burkhart et al., 2006). These earlier studies implied, or explicitly stated, that the extra nitrate peaks probably reflected transport of polluted airmasses to the Greenland ice, with scavenging by snowfall events and perhaps dry deposition of nitric acid and particulate nitrate enhancing snow nitrate concentrations.|
In the present study, the depth profile of isotopic composition of nitrate in a shallow snowpit is presented (along with profiles of nitrate and selected other ion concentrations). The record covers approximately 3 full years, starting in May 2007 at the surface and apparently ending in summer 2004 at 2.1 m depth. Authors identify 5 nitrate peaks, noting that all or part of 4 summer peaks would be expected. They assert that the “extra” nitrate peak was deposited in spring of 2005 and then devote much of the manuscript to making a case that the enhanced concentrations of nitrate along with small decreases in delta O-18, cap delta O-17, and small increase in delta N-15 can all be linked to low ozone column coming out of the winter of 2005 causing increased local production, and deposition, of nitrate. The basic idea is that the smaller ozone column allows for higher UV flux, which could cause more photolysis of nitrate (also hydrogen peroxide) at depth in the snowpack, leading to enrichment of delta N-15 (note, this should also be at depth) in the snow and particularly a higher ratio of OH/O3 above the snow. Relative enhancement of OH could also partly result from greater photolysis of boundary layer O3. If more of the locally produced nitrate came from oxidation of NOx by OH (rather than O3) the oxygen isotopes would be expected to decrease as observed, if locally produced nitrate is a significant or dominant fraction of the total nitrate deposited at Summit.
Having laid out the basic argument based on the single “extra nitrate peak” in this snowpit, in the last 3.5 pages of the discussion the authors seek supporting evidence from an earlier 1-m deep (just over 1 year long) Summit pit and then extend their hypothesis by comparing other years with “spring” nitrate peaks in a firn core to the springtime O3 column in corresponding years.
One major problem that I have with the manuscript is the implicit assumption that much of the nitrate in snow at Summit, and apparently essentially all of the isotopic signature in that nitrate, results from locally produced nitrate. Hastings et al. (2004) argued that postdepostional processes had modest or no discernable impacts on the isotopic composition of nitrate preserved in firn (and subsequently ice) at Summit, a conclusion that was backed up by laboratory studies reported by McCabe et al. (2005 (JGR, 110, 2004JD005484)). This finding was further supported by extensive sampling of surface snow and shallow pits at Summit in summers of 2010 and 2011 when photochemistry is most active, (Fibiger et al. ,2013 (GRL, 40, grl.50659)) and no changes in the oxygen isotopes that could be explained by local processing were observed. As a result of this bias to explain nitrate concentrations and isotopic composition through local processes I feel that the authors were much to quick to dismiss the possibility that spikes outside the broad summer maximum might be related to long-range transport of pollution or possibly biomass burning smoke.
Note that it is possible that Hastings and her group are incorrect, and nitrate at Summit is dominated by local production. However, the discussion of the local processes that may be influencing nitrate in this manuscript is disjointed. The comments of reviewer 2 on the original manuscript made a lot of cogent points, which were dismissed (generally not in a convincing manner) in the authors’ response and largely ignored in this revised version. I agree with nearly all of the issues that referee raised and suggest they must be addressed before this paper should be published.
In particular, I agree with the comment that dating of both the snowpit and the firn core are critical to this story, and suspect in the present version. Starting with the pit, the entire hypothesis is based on assigning the nitrate peak at 1.5 m to spring of 2005 (peak 3’ in Fig. 1). Several weak lines of evidence suggest that this peak could just as plausibly be summer 2005, making the peak labeled 3 sometime later in summer, or even fall, of 2005. (Note that peak 3 has marked decreases in the oxygen isotopic ratios and small increase in delta N-15, and does not look all that much like summer peaks 1, 2 and 4 (especially according to the UW lab).) My case for suggesting that 3’ could be summer 2005 rests on the facts that 1) the depth separation between the “summer” nitrate peaks and “late-winter spring” Na peaks in 2007 and 2006 are quite small, much like the separation between 3’ and the 2005 Na peak, while nitrate peak 3 is about 45 cm higher in the pit, and 2) the depth interval between the partial summer peak (2004) at 2.1 m depth and peak 3 is at least 85 cm compared to 60 and 65 cm between the summer picks for 2005 to 2006 and 2006 to 2007, respectively. Granted, assigning 3’ to be summer 2005 makes the year between summers 2005 and 2006 the fat one, but less anomalously so since compaction increases with depth (annual layer thicknesses should be smaller near 2 m than in the top meter, if accumulation is roughly constant). Further support for a fat annual layer between summers 2006 and 2005 (my suggested redating) may be provided by the measurements of bamboo stakes presented in the supplemental material and in the response to reviewer 2, though it has to be noted that these are measurements of surface height change, not accumulation of snow, and include effects of compaction (See Dibb and Fahnestock, 2004 (JGR, 109, 2003JD004300)). Assuming ~constant compaction over each year, these measurements suggest the surface climbed (relative to the base of the poles) by 65 cm between Aug 2006 and Aug 2007, 80 cm 8/06 to 8/05 and 75 cm 8/05 to 8/04. Note, these complications interpreting the stake measurements make dating method B in the manuscript poorly constrained.
While it is not possible for me to say whether 2005 has nitrate peaks in spring and summer versus summer and fall with information I have, the authors ought to (have to) do a better job validating their subannual dating. If I am correct and the layer at 1.5 m is summer snow, the rest of the manuscript needs to be entirely reworked (or discarded). In a 2 meter snowpit, the visible stratigraphy clearly shows the difference between winter (finer grained) and summer snow (prominent hoar layers), likewise the density profile (lower in the summer). I fully agree with reviewer 2 that nitrate should not be used to identify summer, but excess Cl (or the Cl/Na ratio) is a very unambiguous summer marker (Whitlow et al., 1992; Dibb et al., 2007 (Atmos. Env., 41, j.atmosenv.2006.12.010). It is unfortunate that the Ca data from pit are no good since this is a great spring marker, though as the authors note the annual Na maximum is often just below or in the same layers as the April dust peak. I would be surprised if neither of the isotope labs involved in this study measured the oxygen isotopes in the snow (water) but the manuscript does not mention whether these data exist, these will also show useful winter and summer markers.
The dating of the firn core is even more troubling. While not very clearly described in the manuscript, the response to reviewer 2 makes it clear that “spring” nitrate peaks were identified solely by counting the frequently coincident Na and Ca peaks as annual layer markers and then counting nitrate peaks over the same depth interval. When the latter was larger, the difference was assigned to “spring” deposition regardless of where it may have fallen between a pair of Ca/Na annual markers. As pointed out by referee 2, three of the five example “springtime” nitrate peaks between 5 and 10 m are clearly below (before) both the Na and Ca peaks used to identify late winter/spring (Fig 2). Seems these would have to be early winter, or possibly fall events, yet they are assigned to the spring??? Authors state that it is not possible to resolve seasonality (or differential timing of peaks) in a core sampled at 3 cm resolution, yet one can clearly see this is not correct in the 2 5-m sections presented in this figure (even as deep as 45-50 m the summer nitrate peaks almost always clearly show up above (after) the spring Ca peaks). Similarly, earlier ice core studies mentioned above all seemed confident that they could tell summer nitrate spikes from those coming in at different times through the year in the younger part of the respective records (e.g., Finkel et al., 1986; Whitlow et al., 1992; Yang et al., 1995; Burkhart et al., 2006). As noted in relation to dating the pit, Ca and Cl/Na should provide quite dependable spring and summer marks against which to assess the timing of all nitrate peaks. Visible stratigraphy (light and dark bands) persist to depths equivalent to 50,000 year old ice at Summit, but may require a trained observer to identify with confidence (Alley et al., 1997 (JGR, 102, 96JC03837). If available, the water isotopes in the snow also help with subannual dating. Without much higher confidence that the authors have correctly identified spring nitrate peaks rather than just years with an extra peak due to plume transport, Figure 3 and all discussion of it has very little value.